Paul D. Heideman

Relationship between research in my laboratory and the rest of biology

      How does work in my laboratory relate to other work in our field, and in biology as a whole?  (Click here for a discussion assessing how important our research is.) First, this is basic science research, as opposed to applied research.  Second, my lab's research falls within and between two fields: neuroendocrine physiology and evolutionary biology.  Neuroendocrine physiology is a large field that studies how the combination of the nervous system (brain, spinal cord, peripheral neurons, and peripheral nerves) and endocrine system (hormones, functioning as whole-body chemical signal systems, and the glands that secrete them) regulate body function.  Within neuroendocrine physiology, we study the part of the system that regulates reproduction.  While this is a comparatively specialized discipline, there are still many thousands of scientists world-wide studying these aspects of reproductive regulation.  Within this area of reproductive biology, we study seasonal reproduction (many hundreds of scientists).  We work specifically on rodents (still well above a hundred scientists).  We work specifically on variability in reproductive regulation in order to understand brain variation (no other laboratory that I know of, but I have friends and colleagues in around a half-dozen laboratories who address related questions).

      Within evolutionary biology (many, many thousands of scientists world-wide), we study microevolution (still thousands of scientists) of physiological traits (hundreds of scientists) that are governed by brain function (dozens of scientists, I think).

      In what way, if any, is the research in my laboratory unique?  In general, relatively few scientists address questions that integrate two fields because it takes a lot of time to learn each field.  Physiology and evolutionary biology remains an unusual combination, and so the relatively few scientists who combine them are usually doing work that is in some sense unique.  In the case of the work that we do, I'm not aware of anyone else who is trying to answer the same questions we are--about the nature of natural physiological variation in complex brain pathways.  There probably are at least a few scientists in quite different fields (in research areas I don't follow) who are attempting something reasonably similar.  There are certainly many thousands of scientists studying differences among rat or mouse strains to try to identify the causes of specific diseases.  However, I'm not aware of any other scientists who are using rat strains to try to understand variation for its own sake.  The use of selection experiments followed by physiological studies, like ours on white-footed mice, is an important standard approach within evolutionary physiology.  There have been several laboratories that have carried out these kinds of studies on photoperiodism in rodents, and other studies of this type are ongoing in other research labs (one on another species of Peromyscus, as well as several on hamsters, and several lab groups are doing analogous work on feral sheep).  All of these other labs and projects are focused on using this variation to identify the mechanisms of the photoperiod pathway, rather than trying to understand the nature of variation.  There is no one else even close to doing what we do for the reasons we do it.  In that sense, our research work is unique.

      While our work may be unique, is it important?  If it is important, how important is it?  These are tougher questions to answer.  It's hard for me to answer without wondering if it's just that I'm biased--I think it is very important.  Maybe a better questions is how scientists assess importance and how often scientists turn out to be right in those assessments. 

      At any given time in science, there are some questions that are clearly very important.  In our time, the genome projects are obviously extremely important, as is a great deal of fundamental research in molecular biology, and as is research in ecology on the effects of habitat disturbance, extinctions, and the potential effects of climate change.  Usually these questions gain a large amount of scientists, research money, and effort, for obvious reasons.  At any given time, there are also some questions that are harder to assess, and in some cases impossible to assess.  A classic example comes from the reported response of many researchers to Barbara McClintock's studies of transposable elements in corn.  For much of her career she was apparently regarded by many other scientists as someone on the fringes of science, studying a phenomenon that might not even exist, and that was probably unimportant, except in corn, even if it did exist.  If so, they were wrong; Barbara McClintock earned a Nobel prize for truly revolutionary work.  A more recent example comes from the study of neurogenesis (growth of new neurons) in the brains of adult mammals.  For decades, virtually all neurobiologists accepted a set of studies that appeared to demonstrate that new neurons never developed in the brains of adult mammals.  For a couple of decades, the occasional neurobiologists who obtained evidence of neurogenesis in adult brains were ridiculed.  The question was regarded as so unimportant (in this case because we thought the answer was known), that people couldn't get any funding for the research, and these scientists were either driven out of science or switched to other research questions in order to salvage their careers.  Fernando Nottehohm (working on neurogenesis and neural pathways in birds for the past 30 years), was the only scientist in the area who survived these attacks, and his studies reporting neurogenesis were ridiculed or ignored by most scientists in the field.  What changed?  in the late 1990's, another scientists, Elizabeth Gould, accumulated strong evidence for adult neurogenesis in many mammals, including higher primates, that is now widely (but still not universally) accepted.  Suddenly we recognize that this is an extremely important question, and suddenly adult neurogenesis of the central nervous system one of the hottest topics in neurobiology.

      So where does the research in my laboratory fit?  I'll make a case for its fundamental importance, and then I'll critique that case. 

      Any evolutionary biologist would agree that it is important to know how much and what kind of variation exists in complex physiological systems in natural populations.  There are many other important questions that depend in part on the answer to this particular set of questions.  In addition, a major question in evolutionary physiology is the extent to which complex physiological systems, and especially the brain, have been optimized through evolution by natural selection.   The alternative hypothesis is that complex systems are rarely under strong selection for long enough to be optimized, and that selection has produced complex systems that are mostly just good enough. Almost everyone in the field would probably agree that perfect optimization is impossible, and that it is probably impossible even to define 'optimal function' for a given system; a bigger question is whether complex systems generally function well, or generally function very poorly. There are practical consequences to the answer.  Do most of us have a brain that generally functions optimally, or do we just have a brain that functions adequately, or even relatively poorly?  Is genius the rare individual lucky enough to have a brain that, by a chance combination of genetic and environmental effects has produced a brain that functions optimally?  Do most of us have a brain that just muddles along, with many functions that could be enhanced with appropriate treatment?  Is mental illness often just a consequence of chance combinations  that produce suboptimal function, or is it due to specific causal agents of disease?  If brains are generally optimal in function, then medical or other kinds of treatment should focus only on getting diseased or damaged brains back to normal.  If brains are generally only just good enough, then the implication is that many of us have brains that could function much better, and perhaps we could develop brain-improving treatments. 

      Any physiologist would agree that complex interactions among genes or systems are important in physiology.  Any of physiologist would also agree that our knowledge of those kinds of interactions is pretty limited--that in fact it is very difficult even to estimate how often such interactions occur and how important they truly are.  If these kinds of interactions are important, then answers to these questions will be broadly important in basic physiology and clinical medicine. 

      Here's the critique:  the questions my lab addresses are arguably big and important questions, but our methods may not be adequate to answer them.  It isn't enough merely to address an important question.  To make a contribution, scientists also have to be competent and clever enough to get good and useful answers.  Some questions that are obviously important questions may be unanswerable using currently available methods.  Even if they are answerable questions, we may still choose methods that won't work, or do poor experiments. 

      Are the methods of my laboratory at William and Mary adequate?  Yes, at least to the extent that reviewers for major scientific journals in our field have accepted our papers for publication.  This implies that other knowledgeable scientists think that our results are valuable and our methods good ones.  Are we getting answers to the big questions?  The jury is still out.  What we've learned about the big questions so far, in my assessment, represents a useful advance.  Our finding of high variability in this complex brain pathway in our population of white-footed mice just confirms at least a half-dozen previous and very good studies showing that we should expect this kind of variation.  Our finding that variability exists in multiple locations, that there appear to be multiple ways to be a winter breeder, and that the various states have different costs and benefits is a bigger advance.  Our finding that some strains of laboratory rats are truly photoperiodic is new.  They indicate that rats are a better model system than previously thought for studies on the photoperiod pathway.  However, previous studies had shown that rats do have this pathway, even if the pathway is nonfunctional in most strains.  I think that the most important answer we have thus far is the following:  when we test a candidate source of variation, usually we find variation in that component.  That's actually surprising to me.  For several reasons, I expected that among the many, many possible sources of variation in this complex pathway, only one or a few critical components of the pathway would be variable.  To me, variation at multiple points in this complex pathway supports the 'just adequate brain' hypothesis for brain function, not the 'optimal brain' hypothesis.

      How would I sum up?  Our big questions are truly important in a very broad sense in biology.  Our narrower questions are interesting and relevant to our field.  Our methods are adequate to get some answers to the narrower questions.  We hope that we will contribute to the big questions, but we can't be sure yet.  What we've done thus far is a beginning, and it isn't enough.  It may take years or decades before we have a good sense of how important or unimportant our work has been.  In the meantime, we have a good time thinking about the questions, big and small, and we (most of us, at least) love doing the work, sometimes even when we're doing menial or repetitive tasks.

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Last updated  9/01/2009
College of William and Mary, Department of Biology